EIGHT

Making a Difference and Contributing Useful Knowledge
Principles Derived from Life As a Scholar-Practitioner*

MICHAEL BEER

MY LIFELONG WORK as a scholar-practitioner has made a difference in the life of organizations and individuals; in a few cases, it has had a dramatic impact. Organizations and managers developed and became more effective, and the quality of work life improved. At the same time, I think I can claim that my work has had an impact on knowledge useful for theory and practice.

In this chapter, I articulate principles for developing knowledge that is relevant or actionable or both. I glean these from an examination of more than 40 years of work as a researcher and consultant, often occupying both roles at the same time. These roles have been symbiotic and have led to a broad set of activities ranging from academic research across several content domains; the development of interventions based on knowledge in the field of behavioral science; testing of these interventions through action research; and the formalization of knowledge gained through articles, books, and consulting tools. By repeating this process through many consulting projects in multiple organizational settings over a long time, I have been able to develop systemic practical theories. For example, research on large-scale corporate transformations published in The Critical Path to Corporate Renewal articulates a theory of organizational transformation (Beer, Eisenstat, & Spector, 1990a). My recent book High Commitment, High Performance provides an operating theory of high-commitment, high-performance (HCHP) organizations and how to develop them (Beer, 2009). Most academics and consultants do not engage in such a broad range of activities, and as a consequence, both groups struggle to develop rigorous knowledge that contributes to practice and theory.

Because the term “useful” could have different meanings to each reader, I make a distinction between two forms of useful knowledge. In this chapter, I will discuss lessons for developing both, but I will emphasize the second—actionable knowledge.

1. Relevant knowledge provides managers with general insights about what they should know, do, and be to solve practical problems in a way that achieves specified outcomes. To be useful to managers, findings from relevant research must be written in an accessible manner, but the capacity of managers to implement such research will vary widely depending on their values, skills, and context. Relevant knowledge is often a product of descriptive cross-sectional research studies. It provides academics with knowledge about regularities in the relationship between variables of interest. To be useful for theory, insights from this research must be placed into the context of existing literature and theory. To produce relevant knowledge, the research must focus on a managerial problem. It cannot be primarily designed to test an existing theory or validate previously identified regularities in relationships between variables.

Knowing about relationships between managerially relevant variables does not, however, ensure effective action nor does it allow us as academics to predict with certainty the outcomes of managers trying to employ the knowledge. In short, conclusions from descriptive cross-sectional research never account for all the variance (indeed, statistically significant findings often account for relatively little variance). To be actionable, managers must contextualize relevant knowledge, something they may not be able to do, thus limiting the applicability of the knowledge. Hence the next category becomes critical.

2. Actionable knowledge provides guidance for how managers should go about solving organizational effectiveness, commitment, and performance problems. By definition, this knowledge is relevant. It is typically developed in the context of a specific organization through scholar-practitioners working collaboratively with managers to solve a problem. It provides details about the intervention that managers are advised to enact to achieve specified results—the sequence of steps they are advised to follow and the conditions that must be in place to ensure success. To be theoretically meaningful, scholars must show that the same intervention, under the same conditions, achieves the same results across multiple applications or cases. Actionable knowledge can only be obtained from action research. In my own work, our development of the Strategic Fitness Process (SFP)—an intervention that enables managers to realign their organizations with strategy with commitment—is an example I discuss later.

In short, relevant knowledge is not necessarily actionable, but actionable knowledge is always relevant.

My Development As a Scholar-Practitioner

After receiving my doctorate in industrial and organizational psychology from Ohio State—schooled in the latest research and statistical methods—I made an unconventional career choice. I took a job at Corning Glass Works (now Corning Inc.) as a researcher in the company’s corporate human resource function. Later I founded and grew the company’s Organizational Research and Development Department. I regard this choice and my experience at Corning as seminal. It shaped my identity as a professional and taught me how to use consulting engagements to develop relevant and actionable knowledge.

Though initially hired to do applied personnel research, to produce relevant knowledge for human resource professionals—in effect, to be staff to staff—a number of requests by line managers for hands-on assistance in solving organizational challenges they were facing reoriented me to work as a scholar-consultant. This began a multiple-year journey that changed my identity and practice. By working with general managers, I became more concerned with general management problems—performance, strategy implementation, organization design, senior team effectiveness, and strategic management—domains that for the most part my PhD education did not deal with. Projects with which I became involved were no longer driven by my scholarly interests or existing theories but by urgent problems managers had to solve. I learned how to use grounded consulting experiences and data collection about these problems to develop both relevant and actionable knowledge—knowledge that has been useful for practice and theory.

After 11 years at Corning, I took a faculty position at the Harvard Business School (HBS) where I spent 32 years engaged in teaching, clinical field research, and action research stimulated by consulting engagements. During these years, I also learned to use less traditional research vehicles: case writing (at HBS, cases about management problems are the primary teaching and research vehicles), interaction with executives in executive development programs (particularly an executive program I developed that brought teams of managers with predefined problems to Harvard), and data gathering from participants in executive programs about problems that class discussions brought to the fore. It is the accumulation of knowledge from these different sources over 40 years that enabled me to deepen my insights about organizations and organization development first developed as a scholar-practitioner at Corning. The integration of this knowledge enabled me to develop a relevant and actionable operating theory of high-commitment, high-performance organizations and the path to developing and sustaining them over time, which was recently published as a book (Beer, 2009).

Since becoming an emeritus professor, I have been working as chairman of TruePoint Partners, a research-based management consultancy I co-founded. The firm’s consulting practice, though constantly evolving, is founded on knowledge developed by me and my collaborators over the last 40 years.

Principles for Developing Knowledge for Practice and Theory

It is my professional journey that informs the principles for developing useful knowledge for practice and theory discussed in the following sections. I employ the sequence “practice and theory,” to underscore that useful knowledge for practice and theory must begin with a practical problem defined by managers, not by academics. This point of departure is particularly important if the objective is actionable knowledge rather than only relevant knowledge.

Choose the “Right” Professional Context

My choice of industrial and organizational psychology as my field of study played a role in my professional journey. The field’s scientist-practitioner model made it possible for me to contemplate a job in industry without violating my newly adopted professional identity, something impossible for young scholars obtaining their doctorate degrees in business schools today.

Starting my career as a practitioner played a central role in focusing my professional endeavors on problems. I could not imagine that happening had I chosen academia for my first job. Consider how difficult the norms of the academy and the promotions process make it for young scholars to choose problem-based clinical field research or action research as their primary means of inquiry. And consider how the requirement to publish in normal science scholarly journals predisposes young scholars to do research firmly placed within a theoretical framework and tradition. Such research, by definition, leads to narrowly focused theory testing rather than the development of grounded theory. Once socialized as a normal science researcher, it becomes difficult for most academics to break into other modes of inquiry even after tenure is earned.

My choice of a nontenured position at the Harvard Business School over a tenured appointment at Michigan State, when I left Corning, proved to be critical to my development as a scholar interested in managerial problems. The school’s historic focus on problems in its teaching (case method) and field research encouraged my commitment to solving management problems and deepened my understanding of general management. Because case writing and course development are valued activities at HBS, I was able to use this form of research to develop practical knowledge in the fields of human resources as well as organization effectiveness and change, the focus of two different courses I developed and led (Beer et al., 1985). I might add that HBS policy at the time did not privilege publications in academic journals over publication in journals and books that speak to managers, though this may, unfortunately, be changing.

I do not argue that becoming a full-time practitioner is the only way to form the attitudes and skills needed to develop relevant and actionable knowledge. My colleague Richard Walton, whose whole career was spent in academia (Purdue and HBS), made many important contributions to practice while also contributing to the theory of high-commitment organizations. He did this by helping managers develop high-commitment organizations and through action research documenting successes and failures. Analysis of multiple cases of success and failure enabled distillation of essential design features, change processes required for success, and corporate context needed for success. His predisposition to make a difference undoubtedly was a factor in his choice to develop useful knowledge, but the environment of the Harvard Business School surely supported it. Chris Argyris, Ed Schein, Ed Lawler, Susan Albers Mohrman, Paul Lawrence, Jay Lorsch, and Richard Hackman, among others, are other stellar examples of academics that have made major contributions to practice from an academic base.

Young scholars may ask how they are to get access to organizational settings so they can develop capabilities as scholar-consultants. One way is to participate in executive development programs for senior teams who come prepared with a problem they need to solve. I developed such a program at HBS and ran it for almost two decades. It served to develop consulting skills in several faculty who participated. Because the program was designed with a follow-up session nine months later, it offered multiple case writing and research opportunities. In Chapter 9, On Knowing and Doing, Michael L. Tushman discusses a successor to this program and research that demonstrates the impact of such programs on practice. A second way for young scholars to develop their practitioner skills is to apprentice with independent consultants, small consulting firms, or applied research institutes such as the Center for Effective Organizations (CEO) or the TruePoint Center for High Commitment and Performance I recently co-founded. If business schools are to increase the production of useful knowledge, their norms will have to change to include and legitimize the types of developmental experiences outlined in the preceding paragraphs and the action research that it will produce.

Unfortunately, this legitimization is not happening, so consulting firms and not-for-profit institutes like the CEO remain the primary providers of useful knowledge.

Find a Practical Problem Which You Do Not Know How to Solve

It is not only important that the pursuit of useful information be motivated by real problems but that it be motivated by problems to which the scholar-consultant does not have an answer. I have been fortunate in my career to have had not one, but several, such opportunities. Some of them are described briefly in the following sections to give the reader a “feel” for the type of work that leads to knowledge useful for practice and theory. I employ these examples later to illustrate the principles I will discuss.

The Medfield project

Shortly after arriving at Corning, I received a call from a small manufacturing plant in Medfield, Massachusetts. It was manufacturing medical instruments, a new business for Corning. The plant was the only non-union factory in the company, and its managers wanted to ensure it stayed that way. All had worked in Corning’s unionized plants and worried that unionization would lead to work practices they abhorred and that would undermine the manufacture of high-reliability instruments. The plant’s leaders had read Douglas McGregor’s Human Side of Enterprise (McGregor, 1960) and wanted to become a “Theory Y” plant. Could I help? I said yes. My PhD dissertation was an empirical study aimed at testing the relationship between Theory Y leadership behavior and various human outcomes, so I was thoroughly familiar with Douglas McGregor’s theory. But as soon as I hung up the phone, I realized that I knew nothing about what the practice of Theory Y management looked like or how to help the plant’s leaders transform the organization. Knowing the theory at the level of abstraction specified in McGregor’s book did not provide actionable knowledge.

The resource I had was the literature—Fred Herzberg’s ideas about the importance of challenging work and the then-emerging practice of job enrichment (Hertzberg et al., 1959) as well as the participative management literature. Such top-down theories must, of course, be contextualized when developing interventions for a particular organization, but my familiarity with the academic literature played an important role in this and other action research projects throughout my career. Additionally, I found useful information about practices at Non-Linear Systems, a small manufacturing company in California founded as a high-commitment system.

My lack of knowledge about how to help the Medfield plant change the way it organized and managed work and people released a lot of productive energy in devising interventions. In this and other action learning projects, practical problems I did not know how to solve took me out of my comfort zone and sent me in search of multiple sources of knowledge, a path that made me and my work more relevant. My experience suggests that the search for theories and practices when confronted with practical problems is an important development experience. Professional schools who want to develop scholars capable of developing useful knowledge will have to provide such experiences. Unfortunately, that is not happening in most professional schools, and therefore, such knowledge is not being developed.

Numerous interventions were made: workshops for managers, removal of an assembly line and the creation of whole jobs, quality control delegated to operators, coaching for first line supervisors, the posting of profit and loss as well as other performance measures on the bulletin board, information sessions with doctors who explained to employees how the instrument was used with patients, and visits by employees of one another’s departments that unexpectedly led to identification of manufacturing process problems and their improvement. At the end of three years, the operating and cultural environment had changed dramatically as measured by multiple methods: participant observation, interviews and surveys conducted by a colleague in my department acting as an independent researcher, and the views of higher-level managers.

What useful knowledge did this project develop, and how did it find its way into practice? The Medfield model helped introduce high-commitment management practices to Corning’s other plants. Two decades later, long after I left Corning, its new director of quality said that they were rediscovering that what was learned at Medfield was crucial to Corning’s corporate quality initiative. Useful knowledge gained at Medfield informed the development of General Foods’ high-commitment Topeka dog food plant when I was asked to come and share our experience. Two articles were written: one in an academic journal (Beer & Huse, 1972), and one in a managerial journal (Huse & Beer, 1971). Insights from this project also informed later work and writing.

The EPD project

Because of the credibility I developed with the Medfield project, a new general manager of Corning’s Electronic Products Division (EPD) approached me for help. In our first meeting, he framed his problem as follows:

I said I would help without knowledge about the potential causes of intergroup problems or approaches to solving them. My staff and I employed interviews and a questionnaire to collect data. Based on these data, a set of recommendations to management was made and largely accepted. These asked the senior team to meet to clarify strategy, adopt a strategic management process (at the time I did not know that was the term for what we were proposing) for prioritizing new product development initiatives, redesign the organization as a project team/matrix, and undergo team development to improve their efficacy as a team. At the end of three years EPD had transformed itself, its rate and speed of new product development increased materially, its revenues and profits increased, its culture changed, and its general manager had been promoted to a bigger job on the strength of changes in organization and performance he had achieved.

The EPD project produced many grounded insights about the systemic nature of organizations as well as about key barriers to strategic alignment and the interventions needed to overcome them. My ability to make inferences and develop insights from a combination of observations and more formal data collection grew over the years. It is a skill that, in my view, professionals who seek to develop useful knowledge must find a way to develop, but one that most business schools do not teach or encourage.

Insights gained from the EPD project informed both academics and managers via a symposium at a professional meeting, the development of a bestselling Harvard case (Beer, 1976), and the development of two executive programs about organizational effectiveness and strategic change. And the EPD project contributed significantly to the later development of the Strategic Fitness Process discussed in a following section of this chapter.

Corporate renewal project

Failed efforts at Corning to translate successful change projects in several organizational subunits into a corporate transformation led me to undertake a field study of corporate transformation after I had moved to Harvard. The efforts of corporations to transform in response to Japanese competition offered the opportunity. We identified six large corporations reported by the media to be undergoing a corporate transformation. We gained access and began to collect data: interviews, archival data, and questionnaires. On the basis of these data, we were able to rank order the companies in terms of their relative progress in the transformation and to identify the ingredients for a successful transformation. For the professional interested in developing useful knowledge for practice and theory, methodological flexibility is essential. In this case, a cross-sectional study was the only way to test ideas that I developed at Corning.

We learned that top-down programs were a false start that delayed progress in five of the companies and that a strategy of unit-by-unit change orchestrated by senior management was the key to success in the leading company. By comparing subunits undergoing change across all the companies, we were also able to identify the process of leadership and change that worked at the subunit level. Findings resulted in the book The Critical Path to Corporate Renewal (Beer, Eisenstat, & Spector, 1990a), a finalist for the Academy of Management’s 1991 Terry Book Award and the winner of an award for best book on executive leadership. What I learned at Corning helped me and my co-authors identify patterns in these companies. In addition to the book, an HBR article that was accessible to managers was written (Beer, Eisenstat, & Spector, 1990b). In this instance, relevant knowledge written accessibly led to dramatic changes in at least one corporation. The chief executive officer (CEO) of ASDA (a U.K. grocery chain), who successfully transformed that company and its 200 stores, read the book and employed the unit-by-unit change strategy outlined in it. The HBR article has also found its way into many texts on change and has helped my colleagues at TruePoint and me inform clients about how to lead corporate transformations. And the development of cases about ASDA (Beer & Weber, 1997) led to further insights about corporate transformations and, in turn, led to the development of a theory of change (Beer & Nohria, 2000).

Interestingly, though The Critical Path to Corporate Renewal presents a comprehensive theory of corporate change, my impression is that it has had far more influence in the world of practice than in academia, illustrating the divide between the two worlds.

The BD project

Would I help Becton Dickinson (BD), a global medical technology company, “become a company capable of strategy implementation”? That was the question I was presented with by the company’s CEO and VP of Strategy and Human Resources. BD was having problems implementing its global and business unit strategies. Using my insights about strategic alignment gained in the EPD project and insights from our study of corporate renewal, Russ Eisenstat and I developed what we have since called the Strategic Fitness Process. The process, ultimately implemented by BD in some 35 organizational units—the corporate organization as well as business and operating units—enables senior teams and consultants to collaborate in a co-investigation of the organization’s effectiveness and plan change. SFP guides senior teams through a series of steps that includes (1) development of a two- to three-page statement of strategic direction; (2) commissioning a task force of eight high-performance and high-potential people to interview 100 key people across all parts of the organization as well as customers and other stakeholders; (3) hearing the truth about barriers to strategic alignment (a structure and process are specified to ensure the truth gets on the table safely); (4) a three-day meeting that enables the senior team to diagnose, redesign, and change the organization; (5) critique of the senior team’s plan for change by the task force; (7) mobilization of the organization through engagement and communication; (8) recycling the process to assess progress. Using insights gained in multiple applications of the process, we developed a manual describing these steps in detail to provide actionable knowledge to practitioners (Eisenstat & Beer, 1998).

Through the development of cases about many organizations that employed SFP, we have been able to identify common “silent” barriers to effective strategy implementation and to identify conditions for successful implementation of the process. The formal research involved two research designs. In the first, we conducted a content analysis of what task forces in a dozen organizations reported to leadership teams. These findings are the basis for an emergent theory of organizational effectiveness. In the second, independent researchers were engaged to write cases on a dozen organizations who had implemented SFP. An analysis of these cases by a team of the consultants involved and the independent researchers provided an evaluation of SFP and identification of the conditions for its success. This research has been published in the Sloan Management Review and Harvard Business Review (Beer & Eisenstat, 2000; Beer & Eisenstat, 2004). Three successive CEOs at Becton Dickinson employed SFP soon after they took charge to develop their strategic change agenda. The process is still employed in the company, and top management is employing it again to identify barriers to growth and innovation. Moreover, SFP has become part of TruePoint’s practice and has been employed in well over 200 organizations in some 50 corporations around the world.

Have a Bias for Action Research

For the following reasons, I argue that action research is the best way to develop actionable knowledge.

The process of collaborative problem formulation, diagnosis, and action between managers and scholar-consultants enables the development of systemic grounded theory about causes of problems and means for change that cannot be accomplished through distanced, more narrowly focused, but more precise positivistic methods. On the other hand, normal science is best at validating these theories.

Interventions, including the initial entry into the organization and conversations with management about their problems, allow the action researcher to observe the response (acceptance or resistance) of individuals, groups, and the organizations to the intervention, revealing truths not observable in normal science. That is because normal social science methods rely on what managers say to researchers—their espoused theory—which is almost always different from how they actually behave—their theory in action.

A bias for action leads to the development of social technologies such as SFP. These technologies provide managers with what Fritz Rothlisberger called “walking sticks” (Rothlisberger, 1977). They make knowledge useful to practitioners who may not otherwise have the insights or skills to lead change. For example, SFP has helped managers who saw the need to change but did not know how to engage the total system in such a learning process, an essential leadership capability. Moreover, because social technologies provide detailed guidance for managers and consultants, knowledge is made accessible. For example, SFP has been applied in different industries in several parts of the world by managers who may not naturally have been inclined to do so and in the process have developed new attitudes and capabilities.

Social technologies enable the development of predictive theories. Because they specify outcomes and guide managerial behavior to achieve these outcomes, deviations by managers are measurable. This enables revaluation of the social technology and leads to insights about context, values, and skills required to achieve specified outcomes. Multiple applications of a social technology such as SFP have led to a predictive theory of change, one that specifies behavior and context required for achieving specified outcomes.

Action research enables innovations in organizing, managing, and leading. Managers do this, of course, when they create new managerial practices. However, by collaborating with managers in this process, the researchers can add value. They bring to the conversation extant knowledge from the field of management and arguably improve the new practice. The Medfield and EPD project at Corning reframed for senior executives what was possible in managing people and aligning the organization with strategy. So did a union-management intervention at Corning not described in this chapter. Similarly, the development of SFP at Becton Dickinson reframed for its senior executives how to think about strategy execution and gave them a systemic organizational learning practice they might not have developed on their own. More important, through its use over the years, values and culture have changed.

Maintain an Open Aperture in the Inquiry

The development of useful and usable knowledge requires researchers to have a systemic perspective best achieved by focusing the inquiry on gaps in organizational outcomes—performance, behavior, or both—and to be open to multiple causes. The inquiry cannot be restricted to a small a priori set of content domains, theories, or measurement tools that are of interest to the researcher. To invoke an age-old story, the applied researcher cannot be the drunk looking under the street light for his key because that is where the light is. The inquiry has to consider multiple levels of analysis: individual, interpersonal, group, intergroup, the organizational context, and the context in which the organization is operating. Though clearly all of us have favorite theories that influence where we look, the researcher must guard against that predisposition, one that is deeply baked into our development as academics.

My experience with Corning’s EPD again illustrates this point. The presenting symptom (quoted earlier in this chapter) was interfunctional conflict. It would have been easy to define EPD’s problems that way and suggest well-known and popular intergroup interventions of that time (Blake & Mouton, 1965). By focusing on gaps in performance—the inability of the division to develop new products quickly and effectively—and searching for multiple causes, the diagnosis ultimately also included organizational design (a functional organization that did not enable coordination), senior team efficacy, the top leader himself, and the strategic management process for reviewing new product development initiatives.

Inquiries must, of course, be informed by knowledge from academic research and theories (Bartuneck & Schein, 2010). Scholar-practitioners bring some of this knowledge with them but a search of the literature is also called for. In my experience, however, it is best for the literature search to follow an initial foray of data gathering and analysis of the situation by the scholar-consultant to avoid narrowing the aperture. This principle is again illustrated by the EPD project at Corning. After an initial data gathering and discussions with my team about root causes and potential interventions, I located an article in Administrative Science Quarterly (ASQ) by Paul Lawrence and Jay Lorsch in which they first reported their research on differentiation and integration (D and I), ultimately published as Organization and Environment (Lawrence & Lorsch, 1967). Their conceptualization of D and I in the context of market uncertainty helped explain why EPD, operating in a much more uncertain environment than other Corning businesses, was experiencing unusually severe intergroup conflict. It also offered important findings about the role of “integrators” in cross-functional teams we had been contemplating. It reinforced our conclusion that organization design and role changes were needed. Beginning with this frame, however, would have focused the intervention on organization design and missed essential top team issues and the importance of the change process itself (Schein, 1969). I cannot overemphasize, however, how comforting it was to understand the problems of EPD in the larger context of the Lawrence and Lorsch theory.

Make the Inquiry Collaborative

That collaboration is essential to the development of relevant and actionable knowledge is widely accepted and understood (Shani et al., 2008). In my experience that collaboration will not develop unless the inquiry is focused on an issue central to the general manager’s agenda. That means that discussions have to start with performance gaps and the manager’s hypothesis about cause.

The Medfield project focused on management’s concern with building a culture that they felt they needed to succeed in the labor-intensive, high-quality medical instrument business. The EPD project focused on a more immediate performance problem: speed of product development and collaboration needed to increase the rate of new product development. The Becton Dickinson project focused on the inability of the company to implement its strategy. In the following list, I discuss four desired outcomes collaboration enables and illustrate how collaboration in these projects affected the development of useful knowledge.

1. Develops commitment to inquiry and action. Start by helping managers clarify the gap between current and desired performance and behavior and focus inquiry on diagnosis of why the gap exists. The success of the Medfield, EPD, and BD projects can be attributed to their focus on goals developed with management. All three projects spanned several years and its managers continued to employ the perspective and methods that they had helped to develop.

Can relevant knowledge made accessible to managers create commitment to action? Despite the awards The Critical Path to Corporate Renewal received, the relevant knowledge it imparted was, to my knowledge, employed by only one company, ASDA, the U.K. grocery chain where case research helped us extend our theory of change (see Corporate Renewal Project earlier in this chapter). An extraordinary intellectually inclined leader is the reason. Unfortunately, such leaders are not the norm.

2. Enables researcher to learn from management. My collaborators and I learned a great deal from managers in the action research projects described in this chapter. For example, the Strategic Fitness Process developed at Becton Dickinson was inspired by a process approach to strategy development that the company had institutionalized. SFP was designed to complement that process.

The design of SFP is a product of collaboration, in this case a constructive debate between the CEO and me, the scholar-consultant. Until challenged by the CEO in a high-profile meeting, the stratregic alignment process did not start with strategy. It was an inquiry into barriers to effectiveness. That conversation led us to begin the Strategic Fitness Process with the senior team defining a statement of strategic direction. This statement legitimized SFP and increased commitment to it, despite the company’s conflict-adverse culture at the time. As one senior executive said, “strategy is important to us, therefore learning about barriers to execution is important.” And SFP changed over time as we learned with managers about situational contingencies. For example, when a task force objected vehemently to an action plan produced by its senior team, we learned from the general manager’s response to resolve differences by breaking the senior team and task force members into mixed groups to develop alternatives. It is now part of the SFP toolkit.

3. Enables management to learn from researchers. In all three action research projects described earlier, management learned from us as scholar-consultants. In the Medfield project, we brought in knowledge about practices such as job enrichment and participative management. In the EPD project, we brought in knowledge about organization design and intergroup interventions. Perhaps most important in all three action research projects, we brought in values that became embedded in these organizations through the implementation of new practices. Nowhere was that more clear than at Becton Dickinson where almost all of the senior managers were strategy consultants who did not appreciate the importance of engaging their people to learn about effectiveness problems blocking strategy implementation.

4. Enables longitudinal research. As William James said many years ago, truth emerges over time. It is a function of unfolding events that reveal new facets of the situation. Action research allowed us to be deeply immersed in the organizations over an extended period of time. That allowed me to learn things about the organization and its leaders I did not know at the start of projects. It also allowed evaluation of interventions over time. Our mental models of problems and interventions applied became richer and more comprehensive. Consider how repeated applications of the Strategic Fitness Process at Becton Dickinson allowed us to change the process (see earlier discussion). Over time our understanding of why the process works—its active ingredients—has changed significantly. The rational mental map of alignment we started with has been enriched by other frames: leader legitimacy, emotional engagement, meaning, and leadership development.

Create Structure and Processes for Collaboration

Collaboration over a sustained period of time requires a structure and process by which clients and scholar-consultants co-investigate the client system. It is a way to have periodic conversations about the problem to be solved, the inquiry method, findings and action to be taken. Such a collaborative structure serves as a container for what may become difficult conversations from which both the client and consultant can learn. Without such a container, clients may avoid such conversations, ignore data, or deny them if they are threatening, as such data almost always are in inquiries that ultimately make a difference. And the same container enables scholar-practitioners to learn about the client system. Without such a structure and process for collaboration, the client will not be committed to action and researchers can become distanced from the ever-changing concerns of leaders and the very phenomena they want to understand and study. When scholar-practitioners become distanced, they can easily drift into framing the research in academically interesting but practically unsatisfying ways (Beer, 1982).

There are an endless number of arrangements for collaborations that have and can be developed. In this chapter, I discuss briefly how the Strategic Fitness Process described earlier enables client commitment to change and research. We developed the process to avoid some well-documented pitfalls to client ownership of change: denial and dependence on consultants (Schein, 1969; Argyris, 1970).

By asking top teams to craft a short statement of strategic direction, we ensure that the inquiry has a relevant and useful focus. We have learned that when clients appoint a task force composed of their best people to conduct interviews (with approximately 100 people across the system), it is more difficult for senior teams to deny or ignore the data. In a “fishbowl” structure, task force members discuss findings as a group while senior management sits in an outer U and listens. In this structure, task force members feel safe to speak truth to power. Because top teams, not consultants, conduct the diagnosis in collaboration with consultants and develop action plans then subjected to critique by task force members, SFP increases the quality of the action plan and commitment to it.

Organizational learning processes such as SFP are an aid in collecting data. The quality of the data obtained by task forces, with relatively little training, is as good as that obtained by field researchers, in my experience. With guidance of scholar-consultants and a specified method, themes are developed by a rigorous analysis of interview data collected by the task force. Interviews can be subject to more comprehensive and rigorous analysis by researchers after the fact. I have used task force reports to write rich cases about organizations before, during, and after the intervention (usually over a period of several years), making comparative analysis possible. Employing the same method in multiple organizations has enabled us to generalize findings.

The promise of methods such as SFP that involve clients in data collection is that they enable the development of knowledge clients can use immediately while providing scholar-practitioners with a data set for theory development. If the consultant is not inclined to do the hands-on research, independent researchers can be invited to participate and observe the phenomena.

Use Multiple Methods to Triangulate on the Truth

Multiple methods are essential when developing knowledge useful for theory and practice. Interviews or participant observations or both are the primary methods in problem-centered field or action research. In all four of the projects, these methods led to a grounded map of the territory—a rich theory of the case. In three of the projects, I employed survey data and operating and financial data as well as formal content analysis to hone the emerging theory.

In the EPD project, employee survey data measuring the quality of the collaboration and coordination between each of pair of functions enabled us not only to confirm interview data, but important, to identify where the interfunctional tensions were greatest and, based on this information, to target the parties for an intergroup intervention. These data also enabled more formal evaluation of the change effort and analysis later reported in an academic symposium (Beer et al., 1971).

In the BD project, where SFP was employed, a content analysis of task force findings in 12 organizational units yielded six “silent” barriers to effectiveness. By doing the same analysis for 12 additional task forces in other companies we were able to say with some certainty that these are generic barriers to effectiveness. It was our deep and long-term relationship with each of these organizations, however, that enabled us to understand how these barriers work together to undermine strategy implementation. What has emerged is a theory of organizational effectiveness.

In the corporate renewal field study we triangulated on the truth by employing interviews, survey, and archival data in six companies. Moreover, our data collection included many interviews deep in the organization—in some companies, over 100. And employees were surveyed at multiple levels of the organization.

Cases are an important research tool that served me well. I used many of my own cases together with cases written by others to develop the operating theory of high-commitment, high-performance organizations outlined in my recent book (Beer, 2009).

In field and action research the researcher is one of the instruments by which data are gleaned, processed, and interpreted. For this reason the researcher has a responsibility to question interpretations and conclusions continuously. Partnering with an independent researcher who is not involved as a consultant and whose primary role is data analysis is one way. Presenting findings and conclusions to others and asking them to critique one’s work is another. Allowing time to elapse detaches one and enables one to reformulate interpretations and conclusions. By returning to old cases and research findings, I have been able to draw deeper and in some cases different conclusions.

Be a Groundhog

Scholar-practitioners have to be focused on one or two domains of practice. That is because they have to develop distinctive capabilities—deep knowledge, often tacit knowledge, and skill—in order to be able to deliver value to clients. And scholar-consultants, by definition, become deeply knowledgeable about and skilled in organizational change; that capacity enables them to learn, better than others, about connections between their area of practice and other domains, thus leading to an ever-richer grounded and systemic theory about the phenomena on which their practice is focused.

It is this accumulation of knowledge over time that has enabled me to paint an ever-richer picture of what it takes to develop a high-commitment, high-performance organization. The Medfield project taught me about the sources of low commitment and what it takes to embed high-commitment practices in an organization. The EPD project broadened my horizon to include strategy and began my journey of inquiry into facets of the organization critical for strategy implementation: the senior team, organization design, inadequate strategic performance management, and the role of human capabilities. As I and my team began to focus on changing Corning as a corporation, I began to appreciate the problem of corporate transformation, in particular the problem of spreading change from unit to unit. That led to the corporate renewal research.

When Becton Dickinson’s senior management presented me with their challenge—to help it become a company capable of strategy implementation—I was able to employ all of my experiences and insights to formulate the problem systemically and develop SFP as an intervention.

Be a Boundary Spanner

For knowledge to be useful for practice and theory, it is important for the professional to develop multiple identities and be comfortable operating in and speaking to multiple audiences: managers, internal and external professionals such as organization development (OD) and strategic management practitioners who advise managers, educators who teach aspiring practitioners, and academics. I have always been driven by my desire to be relevant to all these communities, and this motivation has helped me produce knowledge useful to each.

I write for practitioner journals and produce cases and articles that I and others use to teach MBAs and executives. I also speak to managers as well as internal and external consultants. At the same time, I have written for referred journals aimed at academics interested in applied problems and have been active in professional associations such as the Academy of Management and the Society of Industrial and Organizational Psychology, delivering papers and organizing and/or participating in symposia. I also consistently serve on the editorial board of one or more journals. My purpose is to stay in touch with the academic literature and to encourage editorial policies friendly to research useful for practice and theory.

Being a boundary spanner has been a challenge. While practitioners welcome practical knowledge, I have found that academics are much less welcoming. The dominant normal science paradigm makes it hard to publish my findings and ideas in the most prestigious academic journals—the socalled A journals. Instead, I present my findings and ideas in books. They are much better vehicles for the rich narrative needed to present relevant and actionable knowledge that emerges from field and action research. The fact that I get almost no requests to speak about my work in academic settings, other than conferences on change, reflects how big the divide is between normal science academics and those interested in producing relevant and actionable knowledge.

To thrive in two worlds requires a strong sense of purpose and identity, something that I have had to develop over the years. It requires a passion for solving real world problems and at the same time for contributing to theory. I have been helped in this by developing a network of like-minded scholar-practitioners who are rigorous thinkers and practically minded, although their number has declined since the 1960s and 1970s. My home at the Harvard Business School has also been an important source of support and inspiration.

Conclusion

I have used my lifelong experience as a scholar-consultant and field researcher to develop principles for those who wish to develop knowledge useful for theory and practice. I hope this narrative will be helpful to those aspiring to fashion such a professional identification. The work of developing useful knowledge is challenging. As I have tried to show, it requires passion for both making a difference and developing theory. It requires readiness to be drawn into ill-defined practical problems that one does not fully know how to approach or solve, to be comfortable with or foolish enough to live with uncertainty. And one has to be able to live in two worlds with different norms and rules for knowing.

It is not clear to me that all individuals are cut out for such a career. As I have tried to show, my career was shaped by my early choice of a professional context, work inside a corporation as a researcher and consultant though I do not argue that choosing to work inside an organization is the only path, nor that such a path is as open today as it was in the 1960s and 1970s. Academics seeking an identity as scholar-practitioners do, however, have to find ways to embed themselves in real world situations where they collaborate in solving managerial problems. As mentioned earlier, collaborating with research-oriented consulting firms and not-for-profit research centers is one way. Developing relationships with corporate human resources (HR) professionals or line executives attending university executive development programs or developing executive programs with a component of action learning is another. The choices I made were undoubtedly influenced by who I am as a person, by my preference for learning inductively, and by my passion to make a difference in the worlds of ideas and management practice.

As I have tried to show, the dominant academic paradigm and the career system that supports it do not make it easy to develop as a scholar-practitioner, though the creation of the Scholar-Practitioner Award of the Academy of Management and appeals by several academy presidents have helped. For years I have thought that the marketplace for ideas will cause academia to change. The opposite has happened. Business schools have become less relevant and generally eschew the development of actionable knowledge, in sharp contrast, I might add, to the values of medical schools. The task of developing relevant and actionable knowledge has increasingly fallen to other institutions—consulting firms and not-for-profit organizations such as the Center for Effective Organizations.

A career focused on developing knowledge useful for theory and practice will require courage to be different and creativity in shaping such a career. Aspiring scholar-practitioners must avoid blindly following the path to promotion required by the academy. They must make a conscious choice about competencies they want to develop and the place where these can be developed. Most important, they must decide that making a difference matters and find ways to integrate that purpose with their interest in academic research and theory.

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ABOUT THE AUTHOR

Mike Beer is founder and chairman of TruePoint, a research-based management consultancy firm, and Cahners-Rabb Professor of Business Administration, Emeritus, at the Harvard Business School. Mike’s research and practice are in the fields of organization effectiveness, organization change, and human resource management. He has authored or co-authored many articles and ten books. His most recent, published in 2009, is High Commitment, High Performance, which has received several awards from professional associations. Mike has been a consultant to senior management in numerous companies and teaches and speaks in a variety of forums. He began his career at Corning Inc., where he founded and led its Organization Research and Development Department.